Testing a Neurocognitive Model of Distancing Using Transcranial Magnetic Stimulation.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Testing a Neurocognitive Model of Distancing Using Transcranial Magnetic Stimulation. (NCT03698591), a randomized na study. The primary outcome is Change in Self-reported Valence (Distancing) From Baseline to 30 Minutes Post Stimulation..

2. Clinical Question

3. Trial Design

The registry record identifies this as a randomized, double-masked crossover study of real versus sham transcranial magnetic stimulation during an emotion-regulation task. The study is marked completed. The listed enrollment is 40. The recorded start date is 2018-10-31, and the primary completion date is 2019-05-24. The phase is listed as NA, and Duke University is identified as the sponsor.

The two sequence descriptions are TMS followed by sham TMS and sham TMS followed by TMS. In a crossover design, participants receive more than one study condition in a sequence, so comparisons may need to account for the within-person structure and the order in which conditions occur. The record does not describe the statistical handling of sequence, period, or possible carryover effects. It also does not report the interval between conditions or other details needed to evaluate those design features.

The primary outcome records a mean change in self-reported valence from baseline to 30 minutes post stimulation. The posted outcome groups each have n=30. That result count is distinct from the enrollment figure; the record does not explain the participant flow or why the outcome counts differ from enrollment. The population definition for the primary measure is all subjects who completed the study protocol, but further details about analysis populations are not reported in the registry record.

Randomization and masking can reduce some forms of bias, but their presence alone does not establish that all potential biases were controlled. The registry record does not report allocation concealment, masking checks, or a detailed protocol for the statistical analysis. The posted results should therefore be read alongside the information available about the outcome definitions and the limitations of the record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects who completed the study protocol.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All subjects who completed the study protocol.

6. Primary Endpoint

The registry lists the primary outcome as Change in Self-reported Valence (Distancing) From Baseline to 30 Minutes Post Stimulation., measured over baseline, 30 minutes post stimulation.

The primary endpoint is change in self-reported valence from baseline to 30 minutes post stimulation, expressed as a score on a scale. Valence describes how positive or negative a subject feels. After using distancing as an emotion-regulation technique while viewing graphic stimuli, subjects rate how they feel on a 7 point Likert scale ranging from 1 (very negative) to 7 (very positive).

This measure is used to represent the emotional response associated with the task. A change score focuses on how the reported rating shifts from the baseline assessment to the post-stimulation assessment, rather than only describing a rating at one time. The registry record specifies the timeframe and the intended population as all subjects who completed the study protocol.

Self-reported ratings capture participants’ own judgments, rather than a direct measurement of brain activity or an independently observed behavioral response. They therefore address the subjective valence component of the task. The record does not state how the score was calculated if a participant had multiple ratings, how missing ratings were handled, or whether the comparison was adjusted for baseline values. Such details are not reported in the registry record.

7. Results Posted in the Registry

• Transcranial Magnetic Stimulation (TMS): mean 0.66 versus 0.67 on control; difference -0.01 (95% CI -0.29 to 0.28), standardized effect d = -0.01; z-test p = 0.967.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Self-reported Effort (Distancing) From Baseline to 30 Minutes Post Stimulation.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Transcranial Magnetic Stimulation (TMS): mean 3.61 versus 3.55 on control; difference 0.06 (95% CI -0.39 to 0.52), standardized effect d = 0.07; z-test p = 0.783.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Transcranial Magnetic Stimulation (TMS) and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: change in self-reported effort during distancing from baseline to 30 minutes post stimulation. Its reported summaries and recalculated contrast follow the same broad pattern as the primary outcome: the posted group means are close, while the uncertainty interval includes differences in either direction. The secondary result therefore does not provide a clearly contrasting pattern that resolves uncertainty about the primary comparison.

Secondary outcomes can add context by examining another aspect of the task. Effort and valence are related to the distancing task in different ways: effort reflects how demanding participants report the technique to be, while valence reflects how positive or negative they feel. A similar overall pattern across these measures is not proof that the conditions have the same effect on every aspect of emotion regulation. Each outcome measures a particular construct and has its own uncertainty.

The record lists 4 outcome measures and 18 analyses, but only one secondary outcome is posted in the information summarized for the results. It does not report a prespecified hierarchy, a correction for multiple testing, or a rationale linking the listed analyses to each outcome. When several outcomes or analyses are examined, unadjusted results carry less weight because chance findings become more likely across a collection of tests. They are best treated as exploratory unless the analysis plan establishes otherwise.

The secondary finding should not be used to strengthen a claim about the primary outcome beyond what the primary estimate and its uncertainty support. Nor does a non-significant unadjusted result establish the absence of an effect. Taken together, the posted pattern is descriptively consistent across the primary and posted secondary measures, but the limited analysis reporting and lack of a stated multiplicity plan constrain how strongly that consistency can be interpreted.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Change in Self-reported Effort (Distancing) From Baseline to 30 Minutes Post Stimulation.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure, reported as a mean and standard deviation for each condition. A mean describes the average score in the posted group. A standard deviation describes how spread out individual scores are around that mean. Neither statistic alone gives the full uncertainty in a treatment contrast; a confidence interval for the contrast is more informative about the range of values compatible with the data under the calculation’s assumptions.

The simple recalculation contrasts the TMS mean with the sham TMS mean using the posted summary statistics. Its mean difference is -0.006, with TMS minus sham as the direction of comparison. The recalculated 95% confidence interval is -0.291 to 0.279. This is an unadjusted calculation, not an analysis that controls for baseline, sequence, period, or other factors. It also does not use participant-level data. The record does not report the underlying observations, so a paired crossover analysis cannot be reconstructed from the posted means and standard deviations alone.

A confidence interval expresses uncertainty in an estimate under the model and calculation used. It is not a range that contains a known fixed effect with certainty, and its interpretation depends on the assumptions behind the analysis. When an interval includes zero, the data are compatible with no mean difference as well as with differences in either direction. That does not show that the conditions are identical, nor does it by itself establish that any difference is clinically important or unimportant.

The unadjusted p-value for the recalculated contrast is 0.967. In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, and it does not quantify the size or practical importance of an effect. A large p-value can reflect a small observed contrast, imprecision, or both. The confidence interval and the estimate should therefore be considered alongside the p-value.

The registry separately lists analyses using ANOVA and a two-sided t-test. ANOVA is a general method for comparing means across groups or model conditions; a t-test assesses a contrast between means under its own assumptions. In a crossover study, an analysis may need to represent the fact that observations from the same participant are related, as well as the order and timing of conditions. The listed method names alone do not establish which terms were included or how the crossover design was handled. The registry record does not report a full model specification, degrees of freedom, or an explicit mapping from each listed result to the named outcome.

Variation also matters for interpreting a mean difference. If observations are more variable, a given contrast is generally estimated less precisely. A pooled standard deviation can be used to express a mean difference on a standardized scale, but that standardized value does not resolve design issues or replace the original scale. The recalculated standardized difference is -0.011. The calculation is based on posted summary statistics and should not be read as an adjusted or participant-level estimate.

For crossover data, dependence between a participant’s measurements can affect the standard error of a within-person contrast. General statistical practice is to account for that dependence when the analysis is based on repeated measurements from the same people. The posted group summaries do not include the correlation between the measurements, and the registry record does not report whether the sponsor used a paired or repeated-measures approach. Consequently, the simple recalculation is best understood as a transparent, unadjusted check rather than a definitive reanalysis of the trial design.

The sample-size illustrations use the observed effect as a planning reference and apply the assumptions recorded for those calculations: a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect. These assumptions describe the illustration, not the original trial design. The trial’s own sample-size justification and design assumptions are not reported in the registry record.

Multiple outcomes and analyses create a multiplicity issue: the more hypotheses or comparisons considered, the greater the chance that at least one result appears notable by chance if all are interpreted without adjustment. The record lists 4 outcome measures, 18 analyses, and one posted secondary outcome, but does not report a multiplicity procedure or a prespecified hierarchy for interpreting outcomes. General statistical interpretation therefore gives more weight to clearly designated primary outcomes and treats unadjusted secondary findings as exploratory unless the analysis plan supports stronger conclusions.

Why does the crossover structure matter?

In a crossover study, each participant may contribute information under more than one condition. The comparison can then depend on within-participant changes, and those measurements are generally not independent. A method that treats them as unrelated groups may not reflect the design. The registry record does not provide enough information to verify whether the sponsor’s reported analyses accounted for this dependence, so the recalculated comparison should not be mistaken for a complete crossover analysis.

What does the discrepancy mean for interpretation?

The simple recalculation and the listed sponsor analyses do not align as a single, clearly identified analysis of the named primary endpoint. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence. Without an explicit outcome-to-analysis mapping and fuller model details, the listed sponsor p-values should be reported as registry analyses rather than assigned to a particular contrast by inference.

11. Confidence Intervals and Precision

The recalculated mean difference for the primary outcome is -0.006, and its 95% confidence interval runs from -0.291 to 0.279. The interval spans zero and includes values on both sides of it. This means that the posted summary statistics do not pin down the direction of the underlying mean contrast with high precision. The point estimate is near zero, while the interval indicates appreciable uncertainty around that estimate.

A confidence interval is a measure of statistical precision under the calculation and its assumptions. A narrower interval would indicate more precise estimation; a wider interval indicates that a broader range of effects remains compatible with the data. Precision is not the same as truth, clinical importance, or proof of equivalence. The interval should be interpreted in the context of the outcome scale, the study design, and the analysis method.

The interval is recalculated from group-level summary statistics, and the recalculation is unadjusted. It does not incorporate a crossover model, baseline adjustment, or any other model terms not represented by those summaries. The registry record does not provide a sponsor confidence interval for the named primary outcome in the information reported. The sponsor’s own analysis takes precedence where it differs from the recalculation, but the listed sponsor analyses do not explicitly identify which result corresponds to the named outcome.

The standard deviations, 0.565 for TMS and 0.561 for sham TMS, describe the spread of the outcome scores within the posted groups. They do not directly indicate how precise a within-person contrast would be in a crossover analysis. That precision would also depend on the relation between measurements from the same participant, which is not reported. Thus, the recalculated interval is informative as an unadjusted summary-statistic comparison, but it should not be read as a fully design-aware estimate.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, rather than the trial’s original sample-size calculation. The stated assumptions are a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm that the calculation associates with an 80% chance of detecting the specified effect under those assumptions, if that effect and model assumptions were correct. The 90% power column expresses the corresponding planning target for a higher chance of detection. These are prospective planning quantities; they do not tell how likely the completed trial was to detect an effect after the results were observed.

The rows compare planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller the effect targeted, the more participants are required for the same power target. For example, the primary-outcome illustration for 100% of the observed effect is 138,216 participants per arm for 80% power and 185,032 participants per arm for 90% power. Planning for 75% of the observed effect gives 245,717 and 328,946 participants per arm; planning for 50% gives 552,863 and 740,127 participants per arm.

These figures are not observed power. They are sensitive to the unusually small observed contrast used as their planning reference, and they should not be interpreted as a recommendation or as the original design target. The registry record does not report the trial’s own sample-size assumptions or justification. The curve should be read as a planning illustration of how the required sample size changes with the effect used for planning, under the stated assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.006; pooled standard deviation σ = 0.563.
2. n = 2 × (1.96 + 0.842)² × 0.563² / -0.006² = 138,215.7, rounded up to 138,216 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.00600000000000001                      # observed difference in means
sigma <- 0.563003552386661                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3698591)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 138,216 (80% power), 185,032 (90% power)
 75% of observed effect: n per arm = 245,717 (80% power), 328,946 (90% power)
 50% of observed effect: n per arm = 552,863 (80% power), 740,127 (90% power)
power.t.test: 138216.7 
Simulated power at n = 138,216 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry lists several sponsor analyses, including ANOVA results with p-values .019, .021, and .948, and a two-sided t-test result with p-value .108. The simple recalculation from the posted primary-outcome group summaries gives a mean difference of -0.006, a 95% confidence interval of -0.291 to 0.279, and an unadjusted p-value of 0.967. The record does not explicitly map each listed sponsor analysis to the named primary outcome, so those values should not be assigned to it without further information.

The recalculation is a simple unadjusted comparison of posted summary statistics. It does not reproduce a participant-level or crossover-specific model. Differences between it and sponsor analyses could reflect analysis choices or which outcomes and contrasts the reported analyses concern, but the registry record does not establish the reason. No explanation of the discrepancy is reported.

Because the discrepancy is flagged, the sponsor’s own analysis takes precedence over the recalculation. The recalculation remains a transparent check on the displayed means and standard deviations, not a substitute for the analysis used by the sponsor. The record would need to identify the endpoint associated with each analysis and describe the model to support a more direct comparison.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, contrasts, time points, or statistical tests. If each test is interpreted on its own without accounting for the collection of tests, the chance of at least one apparently notable result can increase. This is a general statistical concern, not evidence that any particular result in this trial is false.

The registry record lists 4 outcome measures and 18 analyses, while the results information summarized for the secondary endpoint includes one posted secondary outcome. It reports several ANOVA and t-test results, but does not clearly link every analysis to a named endpoint or specify a primary analysis hierarchy. A multiplicity adjustment, family of hypotheses, or strategy for interpreting multiple outcomes is not reported in the registry record. Consequently, unadjusted secondary results should be treated cautiously and should not be given the same confirmatory weight as a clearly prespecified primary analysis.

The primary outcome population is described as all subjects who completed the study protocol. The outcome groups each have n=30, while enrollment is listed as 40. The record does not explain participant flow, the reasons outcome counts differ from enrollment, or whether all randomized participants were included in any analysis. Missing-data methods, handling of incomplete outcome measurements, and any intention-to-treat analysis are not reported in the registry record.

The crossover design also makes it relevant to know whether participants contributed observations under both conditions and how incomplete sequences were handled. The record does not report the number of participants completing each sequence, whether any periods were excluded, or how the analysis addressed missing measurements. These details matter because the set of observations available for a comparison can affect both the estimate and its precision.

There is not enough information to determine whether analyses were prespecified, whether interim analyses occurred, or whether exclusions or model choices were made after results were examined. Those matters are not reported in the registry record and should not be inferred. The missing detail limits assessment of the robustness of the sponsor’s analysis and the extent to which the listed results reflect a planned testing strategy.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse event figures separately for TMS and sham TMS. For each condition, the number at risk is 30, and the serious adverse events affected count is 0. The record also reports other adverse events with 30 at risk and 0 affected in each condition. Deaths are recorded as 0 for each condition, and no serious adverse event terms are listed.

These figures describe the adverse events recorded in the registry for the reported groups. They do not establish that no events of any kind occurred outside the reporting definitions or observation period, and the registry record does not give additional detail about event collection, timing, severity grading, or follow-up. The posted counts should therefore be read as the reported safety summary, not as a complete characterization of all possible risks.

The trial’s safety figures do not determine whether the intervention is appropriate for any individual. They are descriptive registry information and should be interpreted with the limited reporting context in mind.

17. What the Result Does, and Does Not, Mean

The posted primary-outcome means are similar, and the unadjusted recalculated mean difference is close to zero. However, its confidence interval includes zero and spans differences in either direction. The data therefore do not precisely establish the direction or size of the underlying contrast. A result that is not statistically significant in the recalculation should not be interpreted as proof that TMS and sham TMS are equivalent.

The outcome captures self-reported valence after participants used distancing while viewing graphic stimuli. It does not directly measure brain activity, diagnose a stress-related disorder, or establish a clinical effect in people seeking treatment. The trial’s stated motivation concerns understanding cognitive processes and neural circuits related to distancing, but the posted primary endpoint is a subjective rating at the specified assessment time.

The record’s reported sponsor analyses are not explicitly mapped to the named primary endpoint, and the discrepancy flag indicates that the sponsor analysis takes precedence over the simple recalculation. The recalculated contrast is based on posted summaries and does not account for the crossover structure. These limitations mean that a complete interpretation requires the sponsor’s endpoint-specific model and analysis details, which are not reported in the registry record.

The results do not establish whether any observed score difference is meaningful in practical or clinical terms. The record does not report a threshold for an important difference on the scale, nor does it report an equivalence margin. The posted safety counts are descriptive and do not constitute a guarantee of safety. More broadly, this single registry record cannot establish effects beyond the population, task, conditions, and follow-up it describes.

Accordingly, the most defensible reading is descriptive: the posted group means are close, but uncertainty remains; the sponsor’s analysis takes precedence where it differs from the unadjusted recalculation; and the record lacks details needed to judge the full crossover analysis, missing data, and multiplicity. These findings should not be converted into a treatment recommendation or a claim that an intervention works or does not work.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a randomized, double-masked comparison with a crossover design and a subjective continuous outcome. Each feature shapes interpretation. Randomization can support a fair comparison, masking can limit some expectations, and crossover designs can make within-participant contrasts informative. But the analysis needs to reflect the repeated observations and condition sequence rather than treating the design as a simple parallel-group study.

The gap between enrollment and the posted outcome-group counts also highlights why participant flow and analysis-population descriptions matter. The primary population is defined as those who completed the protocol, but the record does not explain how the outcome counts relate to enrollment. Without that information, readers cannot fully assess how incomplete data or exclusions may affect the estimate.

The result also illustrates the distinction between a point estimate and precision. A near-zero mean difference may look straightforward, yet the confidence interval includes a range of possible contrasts. Statistical interpretation should consider both the estimate and its uncertainty, rather than relying on a p-value alone. The planning illustrations likewise show why sample-size calculations depend strongly on the effect selected for planning, while remaining separate from the trial’s original design rationale.

Finally, the discrepancy between the simple recalculation and the registry’s sponsor analyses makes transparent endpoint-to-analysis mapping essential. Clearly specifying which model addresses the primary question, how crossover dependence is handled, and how multiple analyses are interpreted would allow readers to evaluate the evidence more directly. These are broadly important reporting principles for clinical and behavioral research.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this record constrain interpretation. The trial is described as a crossover, but the registry information does not report how sequence, period, or possible carryover effects were handled. The simple recalculation uses group summary statistics and cannot represent the within-participant relationship without additional data. The sponsor’s model specification is not reported in sufficient detail to evaluate that issue.

The registry lists enrollment of 40, while the posted primary outcome groups each have n=30. The record does not explain participant flow, whether outcome counts refer to complete cases, or how missing measurements were handled. The primary population is defined as subjects who completed the protocol, but there is no reported account of exclusions or analysis populations.

The sponsor analyses are not explicitly mapped to the named primary endpoint, and the discrepancy flag indicates that the sponsor’s own analysis takes precedence over the recalculation. Without a clear endpoint-to-analysis correspondence and model details, the differing p-values cannot be reconciled from the registry record. Multiplicity procedures and a hierarchy for interpreting multiple analyses are also not reported.

The outcome is a self-reported rating collected at the stated post-stimulation time point. The record does not report an important-difference threshold, an equivalence margin, or additional follow-up that would establish the persistence of any change. The intervention descriptions are incomplete in the record, and the information does not provide enough detail to assess all procedural features. These limitations do not invalidate the posted summaries, but they restrict the conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Testing a Neurocognitive Model of Distancing Using Transcranial Magnetic Stimulation. — NCT03698591.
• Registry record last updated 2019-12-17; status last verified 2019-12.
• Results first posted 2019-12-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03698591 is a completed randomized, double-masked crossover study sponsored by Duke University. It compares a transcranial magnetic stimulation task with a sham TMS task during an emotion-distancing paradigm. The recorded enrollment is 40; the primary outcome groups each report n=30.

The primary endpoint is change in self-reported valence from baseline to 30 minutes post stimulation, rated on a 7 point Likert scale. The posted means are 0.662 for TMS and 0.668 for sham TMS. The unadjusted recalculated mean difference is -0.006, with a 95% confidence interval from -0.291 to 0.279 and p=0.967. The record also lists sponsor analyses whose endpoint mapping is not explicit; because a discrepancy is flagged, the sponsor’s analysis takes precedence.

The registry reports one secondary outcome concerning self-reported effort. It does not report enough detail to assess missing-data handling, crossover model specification, multiplicity procedures, or the trial’s original sample-size assumptions. Serious adverse events, other adverse events, and deaths are recorded as 0 in each reported condition group.